Zonisamide vs. Placebo in the Treatment of Alcohol Dependence: Complete Statistical Analysis

1. Trial at a Glance

This page covers the registry results for Zonisamide vs. Placebo in the Treatment of Alcohol Dependence (NCT00595556), a randomized phase 4 study. The primary outcome is Change in Number of Heavy Drinking Days (i.e., 5 or More Drinks Per Day for Men, and 4 or More Per Day for Women)Per Week, by Week.

2. Clinical Question

The trial asked whether zonisamide, compared with placebo, was associated with a change in heavy drinking days among people with alcohol dependence. The primary outcome counted heavy drinking days per week, using a threshold of 5 or more drinks per day for men and 4 or more drinks per day for women. The outcome was assessed from baseline to the end of 12 weeks in treatment.

This is a question about the difference between randomized groups, not simply whether either group changed from its own baseline. A within-group decrease can occur for reasons that affect both groups; the between-group comparison is the relevant contrast for assessing whether the observed changes differ. The registry record identifies the trial as a pilot study. It does not report a detailed target population description or eligibility criteria in the posted outcome information.

3. Trial Design

The registry describes a randomized, triple-masked, parallel-group Phase 4 study of zonisamide versus placebo. It lists UConn Health as the sponsor and reports enrollment of 40 participants. The study status is completed; the recorded start is 2006-07 and primary completion is 2009-05. The registry summary characterizes the project as a pilot study intended to examine potential efficacy and tolerability for alcohol dependence.

Randomization means participants were assigned to treatment groups by chance, rather than by a clinician's choice. In general, this can help make groups comparable at the start of a trial, although chance differences may remain, especially in a small study. Triple masking indicates that the registry identifies three roles as masked, but the specific roles are not reported in the registry record. The method used to generate the random sequence, conceal allocation, and maintain masking is also not reported in the registry record.

The parallel design means the two groups received their assigned conditions over the same study period rather than switching between treatments. The posted arm descriptions identify zonisamide medication treatment and placebo, with 20 participants in each arm. Further details about dosage, treatment adherence, treatment changes, or concomitant care are not reported in the registry record.

The primary outcome concerns change in heavy drinking days per week from baseline to the end of 12 weeks in treatment. The outcome description says weekly measurements were analyzed using a repeated-measures approach, described as SPSS linear mixed models, with an interaction by time (week). It also refers to thirteen time points and 12 measurements. The record does not explain that phrasing further. The registry lists three secondary outcomes: change in drinks per week, change in urge to drink measured by the Alcohol Urge Questionnaire, and change in gamma-glutamyl transferase concentration.

Although randomization and masking are useful design features, neither establishes that the result is precise or free from bias. The enrollment was small, and details needed to assess the conduct of randomization, masking, follow-up, and outcome handling are not reported in the registry record.

4. Participant Flow and Accounting

The registry reports how participants moved through each stage of the study. All counts below are exactly as posted; missing counts are not inferred from other stages.

Overall Study

5. Baseline Characteristics

The table reproduces the baseline characteristics posted in the registry, which describe the participants analysed at baseline and help show whether the randomized groups were comparable.

6. Primary Endpoint

The registry lists the primary outcome as Change in Number of Heavy Drinking Days (i.e., 5 or More Drinks Per Day for Men, and 4 or More Per Day for Women)Per Week, by Week, measured over baseline to the end of 12 weeks in treatment.

The primary endpoint is change in the number of heavy drinking days per week, measured from baseline to the end of 12 weeks in treatment. A heavy drinking day was defined as 5 or more drinks for men and 4 or more drinks for women. The measure is expressed in days per week. The registry describes the posted group values as means with standard deviations.

This endpoint focuses on the frequency of days meeting the specified drinking threshold, rather than on total drinks alone. In general, a repeated weekly measure can describe how an outcome changes over time and can use information from multiple visits. The registry says measurements were taken weekly and analyzed with a repeated-measures model that included an interaction with time (week). That approach differs from a simple comparison of two group-level summary values: it evaluates the pattern across repeated observations according to the model used.

The endpoint is relevant to the trial's stated question because the study concerns treatment for alcohol dependence and the measure records days meeting a heavy-drinking threshold. It is still one particular measure of drinking behavior. It does not, by itself, describe every aspect of alcohol use, functioning, or tolerability. The registry record does not report additional details about how drinking information was collected or how missing weekly measurements were handled.

7. Results Posted in the Registry

• Zonisamide Medication Treatment: mean -0.30 versus -0.20 on control; difference -0.10 (95% CI -0.32 to 0.12), standardized effect d = -0.28; z-test p = 0.382.

8. Secondary Efficacy Endpoints

The registry also posts results for secondary outcomes. For each outcome below, the endpoint type, the test applied to the posted summary statistics, the result and its interpretation are given in turn. Secondary endpoints are usually not adjusted for multiple testing, so they support rather than confirm the primary finding.

Change in Number of Drinks Per Week by Week

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Zonisamide Medication Treatment: mean -2.20 versus -1.40 on control; difference -0.80 (95% CI -13.51 to 11.91), standardized effect d = -0.04; z-test p = 0.902.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zonisamide Medication Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Change in the Urge to Drink Alcohol as Measured by the Alcohol Urge Questionnaire (AUQ)

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Zonisamide Medication Treatment: mean -1.40 versus -0.60 on control; difference -0.80 (95% CI -1.42 to -0.18), standardized effect d = -0.80; z-test p = 0.011.
• Interpretation:
  • The 95% confidence interval excludes no difference, so the mean is statistically lower for Zonisamide Medication Treatment than for the control. This is an unadjusted, secondary comparison, so it is suggestive rather than confirmatory.

Change in Gamma-glutamyl Transferase (GGT) Concentration

• Endpoint type: Continuous: a mean value per participant, compared as a difference in means.
• Test: Unadjusted two-sample z-test for the difference in means, using the posted standard deviations.
• Result:
  • Zonisamide Medication Treatment: mean 8.40 versus 2.90 on control; difference 5.50 (95% CI -16.94 to 27.94), standardized effect d = 0.15; z-test p = 0.631.
• Interpretation:
  • The 95% confidence interval includes no difference, so these data do not show a statistically significant difference between Zonisamide Medication Treatment and the control. The interval gives the range of effects that remain compatible with the data.

Across the secondary outcomes, the posted re-calculations do not show one uniform pattern. The results differ in direction, scale, interval width, and how closely the sponsor-reported mixed-model p-values align with the summary-based calculations. The registry includes change in drinks per week, urge to drink measured by the Alcohol Urge Questionnaire, and gamma-glutamyl transferase concentration. These measures cover different aspects of drinking behavior and a laboratory measure, so they are not interchangeable replications of the primary endpoint.

As with the primary outcome, the sponsor reports mixed-model analyses for the secondary outcomes, while the posted group summaries support simple unadjusted comparisons. Differences between the sponsor p-values and the re-calculated p-values mean that neither set should be silently substituted for the other. The sponsor's reported analysis takes precedence as the sponsor analysis, but the registry does not provide the corresponding model effect estimates or confidence intervals. The summary-based calculations describe the arm-level posted values and their uncertainty under a simpler method.

The secondary findings should be considered alongside, not as replacements for, the primary result. Some secondary comparisons may appear more statistically distinct under one analysis than under another, but that does not resolve the primary discrepancy or establish a consistent overall treatment pattern. The outcomes use different measurement scales and represent different constructs; their numerical estimates cannot simply be combined.

Unadjusted secondary results carry less weight because several outcomes are examined, creating multiple opportunities for an apparently notable result to arise by chance. The registry record does not report a multiplicity adjustment or a prespecified hierarchy for interpreting secondary outcomes. In general, multiple testing can increase the chance of at least one false-positive finding if results are interpreted as confirmatory without adjustment. Given the pilot context, small arm sizes, differing measures, and analysis discrepancies, the secondary outcomes are best treated as exploratory evidence rather than definitive confirmation of the primary finding.

Secondary outcomes registered for this trial, for reference (only those above were recalculated):

• Change in Number of Drinks Per Week by Week
• Change in the Urge to Drink Alcohol as Measured by the Alcohol Urge Questionnaire (AUQ)
• Change in Gamma-glutamyl Transferase (GGT) Concentration

9. Statistical Interpretation

10. Statistical Methods Explained

The registry reports continuous outcomes summarized as means and standard deviations. A mean is the arithmetic average of the observed values, while a standard deviation describes how dispersed individual observations are around that average. These summaries describe each arm separately. To compare randomized groups, the posted re-calculation uses the mean difference: the zonisamide group mean minus the placebo group mean. A negative difference means the zonisamide group’s posted change value is numerically lower than the placebo group’s value; what that means substantively depends on the outcome's direction and definition.

What does the simple comparison represent?

The re-calculated comparison is an unadjusted contrast based on the posted group summaries. It does not use the individual repeated observations or reconstruct the sponsor's mixed model. For the primary outcome, it contrasts the posted means of -0.3 and -0.2 days/week and reports a mean difference of -0.1 days/week. The associated standard error and confidence interval quantify sampling uncertainty under the simple comparison's assumptions. These calculations are useful for making the summary data interpretable, but they cannot replace the analysis that used the trial's repeated weekly measurements.

In general, an unadjusted analysis compares groups without incorporating additional covariates or a longitudinal model. This simplicity can make the calculation transparent, but it may not match the original statistical question or how measurements were collected. The registry says the primary outcome was analyzed using weekly measurements and a mixed model, so the re-calculation should be read as a separate summary-based analysis rather than as a reproduction of the sponsor's method.

Why use a repeated-measures model?

In general, repeated-measures methods address the fact that multiple observations from the same participant are related. A person's weekly values are not usually independent observations in the way values from different people might be treated. A linear mixed model can represent within-person correlation and estimate patterns across time, subject to its specified structure and assumptions. The registry describes the analysis as SPSS linear mixed models and says it tested an interaction with time (week). An interaction with time asks whether the group contrast changes over the course of follow-up, rather than assuming that the contrast is identical at every measurement.

The exact model specification is not reported in the registry record. Details such as the covariance structure, fixed effects, handling of incomplete observations, estimation method, and any baseline adjustment are not reported in the registry record. Consequently, the reported model p-value cannot be fully audited from the posted information. The registry reports the method and p-value, but not a model-based estimate or confidence interval for the primary comparison.

How should a p-value be read?

In general, a p-value measures how incompatible the observed data are with a specified null model, assuming that model and the analysis assumptions are appropriate. A smaller p-value is not an effect-size measure and does not establish that a result is important. It also does not state the probability that the null hypothesis is true. Interpretation depends on the analysis being considered. Here, the sponsor's mixed-model p-value and the unadjusted re-calculated p-value differ, so each must be associated with its own method.

The registry reports p = .012 for the sponsor's primary mixed-model analysis. The unadjusted calculation gives p = 0.382. Those figures do not constitute two estimates from an identical analysis. The sponsor's analysis uses repeated measurements, while the re-calculation uses posted summary statistics. The registry does not provide sufficient model output to determine why the results differ, so an explanation should not be inferred.

What does a confidence interval add?

In general, a confidence interval gives a range of effect values compatible with the data under the calculation's assumptions. It reflects statistical uncertainty about the estimated contrast; it is not a range containing every participant's outcome and it does not account for every possible source of bias. For the unadjusted primary comparison, the posted 95% interval extends to both negative and positive mean differences. That breadth indicates limited precision and means the summary-based calculation is compatible with effects in either direction. The sponsor's model-based interval is not reported in the registry record.

Confidence intervals and p-values are related summaries of uncertainty, but neither makes the underlying design limitations disappear. A precise estimate can still be biased, and a broad interval may reflect limited information even when a point estimate appears suggestive. Interpretation should consider the scale, the magnitude, the interval, the analysis method, and the study context together.

Why does over-dispersion matter?

In general, over-dispersion means that observed variability is greater than a model assumes. If a model understates variability, standard errors may be too small and statistical evidence may appear stronger than warranted. The primary and secondary outcomes are reported as continuous means with standard deviations; the registry does not report an over-dispersion assessment, and it would not be appropriate to assume that a particular over-dispersion problem occurred. For these posted continuous outcomes, the main methods questions are the repeated-measures structure, model specification, missing observations, and the mismatch between the sponsor analysis and simple re-calculation.

The listed standard deviations describe spread in the posted summaries, while the standard errors describe uncertainty in group means used in the re-calculation. Neither should be confused with the confidence interval for the sponsor's longitudinal model, which is not reported. The record's limited model detail means readers can identify the stated approach but cannot independently reproduce it from the posted outcomes alone.

11. Confidence Intervals and Precision

The simple re-calculation for the primary outcome has a mean difference of -0.1 days/week and a 95% confidence interval that spans zero. The interval extends to values below and above zero, so the posted summary data do not precisely establish the direction of the contrast. Its width reflects considerable uncertainty relative to the point estimate. The sponsor's mixed-model estimate and confidence interval are not reported in the registry record, even though its analysis has a reported p-value of .012.

In general, a confidence interval describes a range of effect estimates compatible with the observed data under the analysis assumptions. It is not a prediction interval for individual participants, nor does it include all uncertainty about study design, measurement, or analysis choices. A broad interval can be consistent with several materially different effects. For this trial, the enrollment of 20 participants in each arm limits the information in the simple between-group comparison, while the repeated weekly observations are part of the sponsor's model analysis. The model details needed to evaluate that analysis are not fully reported.

The secondary outcome intervals also vary in width, reflecting differences in the scales and observed variability. The drinks-per-week and GGT comparisons have intervals that extend across zero; the AUQ re-calculation interval is on one side of zero, while its sponsor-reported model p-value is also reported separately. These are distinct analyses, and the simple intervals should not be treated as model-based intervals. No confidence interval for the sponsor analyses is reported for the secondary outcomes.

Precision is not the same as statistical significance. An interval that includes zero signals uncertainty about the direction in the corresponding comparison, while a narrow interval would indicate greater precision under the same assumptions. Neither interpretation alone establishes clinical importance. For the primary endpoint, the missing model-based effect estimate and interval are especially important because the sponsor's reported p-value differs from the summary-based result.

12. Planning a Similar Trial: Sample Size

This is a planning illustration, not a re-evaluation of the original trial. It asks: if a new study wanted to detect a difference like the one observed, or a smaller one, how large would it need to be? It is deliberately not “observed power” of the finished trial, which is not a meaningful quantity.

The planning figures are participants per arm, not total events. They are illustrations based on the observed effect and are not the trial's own original design calculations. The registry's stated planning assumptions are a two-sided significance level of 0.05, equal allocation between the two arms, and a normal approximation; each illustration uses the stated fraction of the observed effect as the effect to detect. The trial's original sample-size assumptions are not reported in the registry record.

The 80% power column describes the number of participants per arm that the planning calculation estimates would be needed for an 80% chance of detecting the specified effect under those assumptions, if that effect were the true one. The 90% power column gives the corresponding planning count for a 90% chance. These are conditional design calculations, not promises about what a future study will find. They are not observed power.

The rows for planning at 100%, 75%, and 50% of the observed effect show how the assumed target effect changes the planning count. A smaller effect is harder to distinguish from random variation, so smaller effects need more participants. For the primary outcome, for example, the illustration for 100% of the observed effect lists 206 participants per arm for 80% power and 276 for 90% power; the 50% row lists 823 and 1,102 participants per arm, respectively. These figures depend on the stated assumptions and the observed effect used to build the illustration. They should not be read as a reconstruction of the original trial's design or as evidence that the completed trial had a particular probability of success.

The planning calculations use a simplified normal approximation and equal allocation. The registry record does not report whether the original study used these assumptions, how it selected its target effect, or whether other design features informed enrollment. The figures are most useful for understanding the consequences of different target effects, not for judging the completed trial by a post hoc power calculation.

13. How the Sample Size Is Derived

Power is the probability that a study of a given size rejects the null hypothesis when a specific true effect exists. It depends on four things: the effect to detect, the variability of the outcome, the significance level (here a two-sided α of 0.05, so z_1−α/2 = 1.960) and the desired power (z_1−β = 0.842 for 80% and 1.282 for 90%).

Formula

n is the number of participants in each arm, Δ is the difference in means to detect and σ is the common standard deviation.

Worked calculation for this trial

1. Observed difference Δ = -0.100; pooled standard deviation σ = 0.362.
2. n = 2 × (1.96 + 0.842)² × 0.362² / -0.100² = 205.7, rounded up to 206 participants per arm for 80% power.

The smaller-effect rows in the table above repeat the same calculation with the effect multiplied by 0.75 and 0.5 (for ratios, applied to the logarithm of the ratio).

R code

alpha <- 0.05
z_a   <- qnorm(1 - alpha / 2)          # two-sided
delta <- -0.1                      # observed difference in means
sigma <- 0.362                     # pooled standard deviation
n_per_arm <- function(power, frac = 1) {
  ceiling(round(2 * (z_a + qnorm(power))^2 * sigma^2 / (delta * frac)^2, 6))
}
for (f in c(1, 0.75, 0.5))
  cat(sprintf("%3.0f%% of observed effect: n per arm = %s (80%% power), %s (90%% power)\n", 100 * f,
              format(n_per_arm(0.80, f), big.mark = ","), format(n_per_arm(0.90, f), big.mark = ",")))

# Check against R's built-in function (t-based, so very slightly larger)
cat("power.t.test:", round(power.t.test(delta = delta, sd = sigma, power = 0.80)$n, 1), "\n")

# Simulation: exact two-sample t-test using simulated means and variances
set.seed(595556)
n    <- n_per_arm(0.80)
reps <- 20000
m_diff <- rnorm(reps, delta, sigma * sqrt(2 / n))             # difference in sample means
s2     <- sigma^2 * rchisq(reps, 2 * (n - 1)) / (2 * (n - 1))   # pooled sample variance
tstat  <- m_diff / sqrt(s2 * 2 / n)
cat(sprintf("Simulated power at n = %s per arm: %.3f (%d replicates)\n", format(n, big.mark = ","), mean(abs(tstat) > qt(0.975, 2 * (n - 1))), reps))

Output from running the code

100% of observed effect: n per arm = 206 (80% power), 276 (90% power)
 75% of observed effect: n per arm = 366 (80% power), 490 (90% power)
 50% of observed effect: n per arm = 823 (80% power), 1,102 (90% power)
power.t.test: 206.7 
Simulated power at n = 206 per arm: 0.795 (20000 replicates)

The simulation draws many sets of group means and variances at the planned sample size and counts how often the two-sample t-test rejects the null. It should land close to the target power; at very small required sample sizes it can fall below it, because the normal approximation is rough there.

14. Analyses Reported by the Sponsor

The registry reports the sponsor's primary analysis as a Mixed Models Analysis with p = .012. It does not report the model-based effect estimate or confidence interval. The summary-based re-calculation instead compares the posted arm means and gives a mean difference of -0.1 days/week, a 95% interval spanning zero, and p = 0.382. These results differ, and the sponsor's own analysis takes precedence when describing the sponsor-reported finding.

Precedence does not remove the need to state the discrepancy. The re-calculation is a simple unadjusted comparison from posted summary statistics; the sponsor's analysis uses repeated measurements over time. Different analysis methods can use different information and answer different statistical contrasts. However, the registry record does not give enough detail to establish which model specification or data handling explains the difference. It would be inappropriate to treat the simple comparison as a correction to the sponsor's analysis or to claim that the model result has been independently reproduced.

The same issue appears in the reported secondary analyses: each has a sponsor mixed-model p-value and a separate summary-based re-calculation. The sponsor analysis is the registry's reported inferential analysis, while the re-calculation supplies a transparent, unadjusted perspective based on the posted means, standard deviations, and group sizes. Model-based estimates and confidence intervals are not reported in the registry record. Accordingly, the two approaches should be described distinctly, not merged into a single estimate or presented as if they agreed.

15. Multiplicity, Missing Data and Analysis Populations

The registry lists one primary outcome and three secondary outcomes, and reports five outcome measures and five analyses overall. It does not report a multiplicity-control strategy, such as an adjustment to account for testing several outcomes, or a hierarchy specifying which secondary tests would be interpreted only after a primary result. This matters because examining multiple outcomes can make an isolated small p-value less persuasive than a result from a single prespecified test. The exact impact depends on the analysis plan and the relationships among outcomes, which are not reported in the registry record.

The registry identifies the primary measure and describes a mixed-model approach, but it does not report a complete statistical analysis plan. The timing of any final model decisions, any interim analyses, and the original sample-size justification are not reported in the registry record. No interim analysis information is reported in the registry record. Without these details, readers cannot assess whether all analyses followed a prespecified plan or how any analysis choices were made.

Information on missing data and analysis populations is also limited. The posted summaries list 20 participants in each arm, but the registry record does not state whether these are randomized, treated, or outcome-analysis populations for each measure. It does not report the amount or pattern of missing weekly observations, reasons for missingness, or the method used to handle incomplete data in the mixed models. It also does not report whether any participants were excluded from a particular analysis or how departures from assigned treatment were handled.

In general, missing data can affect a treatment comparison when the probability of having an observed outcome is related to the outcome itself or to treatment assignment. Mixed models can use incomplete repeated observations under assumptions about the missingness process, but the suitability of those assumptions cannot be evaluated from the method label alone. The registry record does not provide enough detail to determine which assumptions were made or whether sensitivity analyses were conducted.

These omissions do not establish that analyses were inappropriate; they limit how fully the posted results can be assessed. The study's small size, multiple reported outcomes, unreported multiplicity handling, and incomplete reporting of analysis populations and missing data all call for cautious interpretation.

16. Safety Results

The registry reports serious adverse events as affected participants divided by participants at risk.

Other (non-serious) adverse events

Participants with at least one non-serious event at or above the registry's 0% reporting threshold.

Most frequent non-serious adverse event terms

The adverse-event figures report zero serious adverse events among 20 participants at risk in the zonisamide arm and zero among 20 at risk in the placebo arm. The registry also reports 16 participants with other, non-serious adverse events in each group, with 20 at risk in each arm. Deaths are not reported in the posted figures. The registry does not list serious adverse event terms.

These counts describe what the registry reports for the trial; they should not be interpreted as proof that no serious events occurred outside the reported record or that the treatments have equivalent safety. With 20 participants at risk per arm, the study has limited ability to characterize uncommon events. The counts do not describe event severity beyond the serious/non-serious grouping, timing, duration, relatedness to treatment, or whether an individual experienced more than one event. Those details are not reported in the registry record.

The equal count of participants with other adverse events does not mean the specific events were identical between groups. The registry does not provide the event terms or a detailed breakdown for those events. Safety interpretation is therefore limited to the posted participant counts and the absence of reported serious events in these arm summaries.

17. What the Result Does, and Does Not, Mean

The trial record describes a randomized pilot comparison of zonisamide and placebo for alcohol dependence. The primary outcome was change in heavy drinking days per week during 12 weeks of treatment. The sponsor's reported mixed-model analysis gives p = .012, while the simple unadjusted re-calculation from the posted group summaries gives a mean difference of -0.1 days/week and p = 0.382, with a broad interval spanning zero. The sponsor's own analysis takes precedence as the reported sponsor result, but the discrepancy and missing model effect estimate limit how fully that result can be interpreted.

A p-value is not a measure of effect size, clinical importance, or probability that a treatment works. The registry's sponsor p-value alone does not show the magnitude of the model-based contrast, because that estimate and its confidence interval are not reported. The summary-based calculation provides a numerical contrast, but it is a different analysis and is imprecise. Both points need to be kept in view.

The secondary results add information about other measured outcomes, but they do not eliminate uncertainty in the primary comparison. Multiple outcomes were reported, and the registry record does not describe multiplicity adjustment or a prespecified testing hierarchy. In general, secondary results from a small pilot are more appropriately treated as exploratory when the statistical plan and multiplicity handling are unavailable.

Nor do the adverse-event counts establish broad safety. The registry reports zero serious adverse events in both groups and 16 participants with other adverse events in each group. The sample size and lack of event details limit what those counts can say about the range or frequency of harms.

Overall, the record documents a completed randomized comparison and provides group summaries and sponsor p-values. It does not provide enough model output, missing-data detail, multiplicity information, or safety detail to support a comprehensive assessment of the size, precision, and robustness of all effects. The findings should be understood in the context of a small pilot study, not as a definitive estimate for all people with alcohol dependence.

18. Why This Trial Matters Statistically

This trial illustrates why statistical interpretation depends on more than a single p-value. The sponsor's primary mixed-model analysis reports p = .012, while an unadjusted calculation from the posted summaries gives p = 0.382. These values come from different methods and should not be treated as equivalent. The contrast makes transparent reporting of effect estimates, confidence intervals, model specification, and data handling especially important.

The repeated weekly design also raises a central methodological issue: observations from one participant over time are related. A longitudinal mixed model can account for that structure, but the method name alone is not enough to reproduce or evaluate the analysis. The registry describes the analysis generally, yet does not report the full specification or model-based estimate and interval. This limits independent assessment even when a p-value is available.

The pilot size matters for precision. With 20 participants in each arm, the simple primary comparison has a broad interval that spans values in both directions. That is a useful reminder that a point estimate is not the same as a well-determined effect. The planning illustrations also demonstrate how the required sample size changes when the target effect is smaller, but those figures are not the original design rationale and are not observed power.

Finally, the record lists multiple secondary outcomes and provides safety counts, while leaving multiplicity, missing data, analysis populations, and detailed event descriptions unreported. These are not merely administrative details: they affect how confidently readers can interpret apparent patterns and how well they can distinguish confirmatory evidence from exploratory findings. The trial is statistically informative as an example of the value—and limits—of registry outcome reporting.

19. Limitations

• The posted summary statistics are the only data these results rest on; patient-level data, full protocols and statistical analysis plans are not available.
• Recalculated results are simple, unadjusted calculations from posted summaries. They do not replace the sponsor's prespecified analysis.

Several limitations are specific to the information recorded for this trial. It is described as a pilot study with enrollment of 40 and 20 participants in each arm, so the posted group comparisons are based on a small sample. The primary summary-based interval is broad, and the sponsor's model-based effect estimate and confidence interval are not reported. The difference between the sponsor's mixed-model p-value and the unadjusted re-calculation cannot be resolved from the registry information.

The record describes weekly measurements and a repeated-measures model, but does not report the model specification, covariance structure, covariate adjustment, or detailed treatment of missing observations. The wording about thirteen time points and 12 measurements is not explained further. The analysis populations for the posted outcomes are not identified beyond the arm counts.

The registry does not report the original sample-size justification, a full statistical analysis plan, interim analysis information, or multiplicity handling. It also does not report detailed eligibility criteria, dosage, adherence, or the specific roles masked in the triple-masked design. These are limits on what can be assessed from the record, not evidence that particular procedures were absent.

Safety information is limited to serious and other adverse-event participant counts. Serious event terms are not listed, deaths are not reported in the posted figures, and details about event type, timing, severity, or treatment relationship are unavailable. The equal counts for other adverse events do not show whether the event types were the same.

The secondary outcomes measure distinct constructs, and the record does not describe multiplicity control. Consequently, isolated secondary findings should not be taken as definitive evidence, especially when sponsor and summary-based analyses differ. These limitations constrain interpretation of the reported results and the degree to which the analyses can be independently reproduced.

20. Related Tutorials

21. Related Statistical Calculators

22. Sources

• ClinicalTrials.gov: Zonisamide vs. Placebo in the Treatment of Alcohol Dependence — NCT00595556.
• Registry record last updated 2010-10-15; status last verified 2010-09.
• Results first posted 2010-10-15.
• Data retrieved from ClinicalTrials.gov on 2026-11-09.
• Group sizes, means, event counts and sponsor-reported p-values are reproduced as posted. Effect estimates, confidence intervals and p-values not attributed to the sponsor are independently calculated from the posted summary statistics.

23. Record Summary

NCT00595556 is a completed Phase 4, randomized, triple-masked, parallel-group pilot study sponsored by UConn Health. It compared zonisamide with placebo for alcohol dependence and reports enrollment of 40 participants, with 20 in each arm. The recorded study start is 2006-07 and primary completion is 2009-05.

The primary outcome was change in heavy drinking days per week from baseline to the end of 12 weeks in treatment. The registry reports a mixed-model p-value of .012, while the simple unadjusted calculation from the posted group summaries gives a mean difference of -0.1 days/week and p = 0.382. The sponsor's analysis takes precedence as the reported sponsor result, but the difference remains unresolved in the available record.

Three secondary outcomes and adverse-event counts are posted. Model-based effect estimates and confidence intervals, detailed missing-data handling, multiplicity procedures, and the original sample-size justification are not reported in the registry record. The findings should be interpreted as results from a small pilot comparison with limited precision and incomplete statistical detail.